Comparison Between Thrombolysis and Primary Percutaneous Coronary Intervention (PCI) to Treat ST-Segment Elevation Myocardial Infarction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison Between Thrombolysis and Primary Percutaneous Coronary Intervention (PCI) to Treat ST-Segment Elevation Myocardial Infarction (NCT00806403), a randomized phase 4 study. The primary outcome is Number of Patients With ST-segment Elevation Resolution Equal or More Than 50%.

2. Clinical Question

The central contrast is therefore between two treatment strategies and an early electrocardiographic marker, rather than a direct comparison of mortality as the primary outcome. The primary result concerns participants meeting a prespecified threshold for resolution in the lead with the most prominent ST elevation at inclusion. It does not, by itself, answer whether the strategies differ in later clinical outcomes. Death, reinfarction, and stroke are listed as secondary outcomes at 30 days, and their interpretation is separate from the primary endpoint.

3. Trial Design

The registry describes a Phase 4, randomized, parallel-group trial with no masking. It records 205 participants and lists acute myocardial infarction as the condition. The study is marked completed. The sponsor is Sahlgrenska University Hospital. The registry records a start in 2001-11 and primary completion in 2003-06.

The randomized comparison assigned participants to a thrombolysis strategy or an invasive strategy. Reteplase 10+10 U is listed as a drug intervention, and primary PCI as a procedure. The official title further describes thrombolysis and low molecular weight heparin compared with abciximab and low molecular weight heparin followed by PCI. The brief summary says the strategies were to begin as early as possible, preferably before hospital arrival. Arm-specific descriptions beyond those details are not reported in the registry record.

The stated objective connects early treatment with two measures: resolution of ST-segment elevation 120 minutes after inclusion and TIMI flow grade at mandated coronary angiography 5 to 7 days after inclusion. The posted primary endpoint result is the count meeting the ST-segment resolution threshold. The registry also lists five outcome measures and five analyses, but the record excerpt identifies only the primary endpoint and three secondary clinical outcomes by name.

Randomization is intended, in general, to make the comparison less vulnerable to systematic baseline differences between groups. With no masking, participants and clinical personnel were not masked according to the registry. The record does not report details about random sequence generation, allocation concealment, treatment crossover, or adherence. Nor does it report the original sample-size justification or further operational details of the two treatment pathways. Those missing details limit how fully the trial conduct can be assessed from the registry record alone.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was made on intention to treat(ITT) basis.Patients with electrocardiograms (ECGs) suitable for analysis at inclusion and at 120 minutes therafter were included in the analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients With ST-segment Elevation Resolution Equal or More Than 50%, measured over 120 minutes after inclusion.

The primary endpoint counts participants with ST-segment elevation resolution equal to or greater than 50% at 120 minutes after inclusion. Resolution was measured in the lead with the most prominent ST elevation at inclusion. The endpoint is therefore a binary measure: each participant either met the stated threshold or did not, and the arm-level result is a count rather than a continuous measurement of the degree of resolution.

The registry's stated objective uses this early electrocardiographic measure to compare the response to the two treatment strategies. In general, a threshold-based endpoint can make a result easier to interpret as the proportion of participants reaching a defined response. It also discards information about how far a measurement lies above or below the threshold; participants with different degrees of resolution can be grouped together if they fall on the same side of the cutoff.

The primary analysis is described as intention to treat, while the endpoint population is specified as patients with electrocardiograms suitable for analysis at inclusion and at 120 minutes afterward. This means the posted endpoint is tied to availability of analyzable electrocardiograms at both times. The registry does not report how many otherwise eligible participants lacked usable recordings or how such missing measurements were handled.

TIMI flow grade at coronary angiography 5 to 7 days after inclusion appears in the objective, but it is not the named primary outcome result analyzed. The primary endpoint should not be conflated with death, reinfarction, or stroke, which the record lists separately as secondary outcomes at 30 days.

7. Results Posted in the Registry

• Invasive: 68.9% (51/74) versus 62.7% (47/75) on control; risk difference 6.3 percentage points (95% CI -8.9 to 21.5), risk ratio 1.10 (0.87–1.39); unadjusted two-proportion z-test p = 0.421.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Death

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Invasive: 3.0% (3/101) versus 3.8% (4/104) on control; risk difference -0.9 percentage points (95% CI -5.8 to 4.1), risk ratio 0.77 (0.18–3.36); unadjusted two-proportion z-test p = 0.730.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Invasive and the control. The interval gives the range of effects that remain compatible with the data.

Reinfarction

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Invasive: 0.0% (0/101) versus 1.9% (2/104) on control; risk difference -1.9 percentage points (95% CI -4.6 to 0.7); unadjusted two-proportion z-test p = 0.161.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Invasive and the control. The interval gives the range of effects that remain compatible with the data.

Stroke

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Invasive: 0.0% (0/101) versus 2.9% (3/104) on control; risk difference -2.9 percentage points (95% CI -6.1 to 0.3); unadjusted two-proportion z-test p = 0.086.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Invasive and the control. The interval gives the range of effects that remain compatible with the data.

The registry reports death, reinfarction, and stroke at 30 days as secondary outcomes. Across these endpoints, the posted event counts are numerically lower in the invasive group than in the thrombolysis group. The primary endpoint, in contrast, has a numerically higher proportion meeting the ST-segment resolution threshold in the invasive group. This is a coherent direction in the observed counts, but it is not enough to establish a reliable difference in clinical outcomes.

The secondary outcomes are distinct from the primary electrocardiographic response. An early change in ST-segment elevation and a clinical event by 30 days are not interchangeable measures. The secondary findings do not prove that the primary outcome predicts later clinical benefit, nor do they independently validate the primary result. They should be viewed as additional, limited evidence about other outcomes assessed by the trial.

There are few events for these outcomes, including endpoints with no events recorded in one group. In general, sparse event data tend to yield imprecise comparisons: small changes in the observed counts can substantially affect an estimate. The record's reported Fisher Exact p-values for the secondary outcomes do not resolve that limitation, and the posted risk-difference intervals for the recalculated comparisons include zero.

Unadjusted secondary results also carry less weight when several outcomes are examined. If each result is considered separately without accounting for the number of comparisons, chance findings become more plausible across the collection of tests. Whether a multiplicity adjustment or hierarchy of secondary endpoints was specified is not reported in the registry record. The secondary outcomes are therefore best treated as exploratory rather than as independent confirmatory evidence.

The overall pattern is relevant for describing what was observed, but it should not be used to overstate certainty. Interpretation depends on the small event counts, the lack of reported multiplicity details, and the fact that the registry provides no further analysis-plan explanation for these outcomes.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Death
• Reinfarction
• Stroke

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is analyzed? The primary outcome is binary: it counts participants who reach the stated ST-segment resolution threshold. For this kind of outcome, a comparison can be expressed as a difference between the groups' event proportions. The posted recalculation uses an absolute risk difference, with the invasive group compared against thrombolysis. An absolute difference keeps the contrast on the scale of the outcome: it describes the separation between the two observed proportions rather than expressing one as a multiple of the other.

In general, risk differences are useful because they express the amount of separation on the original probability scale. Their interpretation depends on the direction convention. Here, the reported estimate is invasive minus thrombolysis, so a positive value corresponds to a higher observed proportion meeting the threshold in the invasive group. That direction describes the sample estimate only; uncertainty around it must also be considered.

What does a confidence interval describe? A confidence interval gives a range of values compatible with the data and the method's assumptions at a stated confidence level. The primary risk-difference interval runs from -0.089 to 0.214. Since it crosses zero, the data do not pin down the direction of the underlying difference with precision. The interval includes a negative difference, no difference, and a positive difference. The range is not a guarantee that the true effect lies inside it, and it is not a statement that every value in the interval is equally plausible.

In general, the width of a confidence interval reflects both the amount of information in the data and the variability of the outcome. Binary outcomes with relatively few participants can yield substantial uncertainty, particularly when event counts are limited. A confidence interval should be read alongside the point estimate, event counts, and design rather than as a stand-alone verdict.

What does the p-value add? A p-value measures how unusual the observed data, or data more extreme, would be under a specified null hypothesis and analysis method. The registry reports a Fisher Exact analysis for the primary comparison, with p = 0.56. The unadjusted recalculation from posted summary statistics gives p = 0.421. These values are method-dependent summaries and do not measure the probability that the null hypothesis is true, the size of the effect, or whether an effect matters clinically.

Fisher's exact test is a general method for comparing binary outcomes in a two-group setting. It uses the observed counts and is often used when event counts are sparse. The registry labels its reported test as Fisher Exact, but does not provide a test statistic, further calculation details, or a confidence interval for that test. The posted risk-difference estimate and interval provide a complementary effect-scale description.

Why look at both absolute and relative measures? The recalculation also includes a risk ratio of 1.1 with a 95% confidence interval from 0.872 to 1.387, and an odds ratio of 1.321 with a 95% confidence interval from 0.670 to 2.605. In general, the risk ratio compares the proportions as a ratio; the odds ratio compares the odds of the event. These relative measures use different scales from the risk difference, so their numerical values should not be directly compared as though they meant the same thing. Their intervals include the null value for a ratio, which is 1, while the risk-difference interval includes its null value, zero. Each measure remains uncertain.

What analysis population is described? The registry says the primary analysis was made on an intention-to-treat basis. It also specifies that patients with electrocardiograms suitable for analysis at inclusion and 120 minutes afterward were included. In general, intention-to-treat analysis aims to retain participants in the groups to which they were assigned, regardless of treatment received. The additional requirement for analyzable recordings means the registry's endpoint population is restricted by measurement availability. The record does not give enough information to determine how missing recordings were handled or whether all randomized participants contributed to the primary outcome analysis.

How should multiple outcomes be considered? The registry identifies several outcomes and analyses, including the primary response and secondary clinical events. Testing multiple outcomes can increase the chance of finding at least one apparently unusual result by chance if each is interpreted as a separate confirmatory test. In general, multiplicity procedures can control that issue, but the registry record does not report whether any adjustment was planned or applied. The secondary findings should therefore be interpreted with that uncertainty in mind, not as independent confirmations.

What can the sample-size illustrations tell readers? The listed planning calculations use the observed effect as a starting point and illustrate hypothetical future sample sizes under stated assumptions. General power calculations describe the chance of detecting a specified effect if that effect and the planning assumptions hold. They do not alter the uncertainty in the completed trial or show whether the trial itself had adequate power. The original trial's sample-size justification and design assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.062, and its 95% confidence interval extends from -0.089 to 0.214. The interval spans zero, so the observed direction is not estimated precisely enough to exclude a difference favoring either group. Its positive endpoint allows a larger increase in the proportion meeting the threshold in the invasive group; its negative endpoint allows a lower proportion in that group. These bounds describe uncertainty on the absolute difference scale.

The interval's breadth matters as much as the point estimate. The data do not locate the underlying difference narrowly around 0.062. Thus, the observed difference should not be treated as a precise estimate of what would occur in a broader population. The registry does not give a clinically meaningful difference threshold, so the interval cannot be classified against such a threshold.

The recalculated risk ratio is 1.1, with a 95% confidence interval from 0.872 to 1.387. The recalculated odds ratio is 1.321, with a 95% confidence interval from 0.670 to 2.605. In general, relative measures can look different from absolute measures because they use different scales. Both ratio intervals include 1, the null value for a ratio, just as the risk-difference interval includes zero.

The primary endpoint counts and denominators also help explain the uncertainty: 47 of 75 participants met the threshold in the thrombolysis group, compared with 51 of 74 in the invasive group. The total enrollment is 205, while the primary outcome denominators are smaller. The record ties primary analysis eligibility to electrocardiograms suitable at both time points, but does not report missing-measurement counts or their handling. That missing information limits assessment of how precisely the analyzed participants represent everyone enrolled.

Confidence intervals quantify sampling uncertainty under an analysis method; they do not account automatically for every possible bias, missing-data problem, or difference in trial conduct. Precision should therefore be read together with the endpoint definition, analysis population, and registry reporting limitations.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial's original design justification. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

For planning at 100% of the observed effect, the illustration gives 903 participants per arm for 80% power and 1,208 participants per arm for 90% power. At 75% of the observed effect, the corresponding figures are 1,623 participants per arm for 80% power and 2,172 participants per arm for 90% power. At 50% of the observed effect, they are 3,690 participants per arm for 80% power and 4,939 participants per arm for 90% power.

In plain terms, the 80% power column represents a planning target with an 80% chance of detecting the chosen effect under the assumptions if that effect is the true one. The 90% column uses a higher chance-of-detection target under those same conditions. A smaller effect is harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm.

These values are not observed power. They are hypothetical planning illustrations, not a retrospective measure of whether the completed trial was successful or adequate. They also do not establish that the observed effect is a reliable estimate for future planning; the observed estimate itself has uncertainty, reflected in its confidence interval. The original sample-size assumptions and justification are not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.627; treatment proportion p₁ = 0.689; average p̄ = 0.658.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6709 = 1.3150.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6694 = 0.5634.
4. n = (1.3150 + 0.5634)² / (0.0625)² = 902.6, rounded up to 903 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.626666666666667                          # control proportion
p1 <- 0.689189189189189                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(806403)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 903 (80% power), 1,208 (90% power)
 75% of observed effect: n per arm = 1,623 (80% power), 2,172 (90% power)
 50% of observed effect: n per arm = 3,690 (80% power), 4,939 (90% power)
power.prop.test: 902.6 
Simulated power at n = 903 per arm: 0.800 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary comparison as a Fisher Exact analysis with p = 0.56. A separate unadjusted calculation from the posted arm-level summary statistics gives p = 0.421 for the primary comparison. The registry record labels the reported test but does not give enough detail to reconcile the difference between these p-values or reproduce the sponsor's calculation fully.

The sponsor-reported p-value should be kept distinct from the recalculated effect estimate and confidence interval. The recalculation describes the risk difference as 0.062, with a 95% confidence interval from -0.089 to 0.214. It is an unadjusted calculation from the posted summary statistics, rather than a replacement for the registry's reported analysis. The registry does not report a discrepancy flag, but the numerical p-values should not be presented as if they were identical.

In general, a p-value depends on the chosen statistical test and its assumptions, while an effect estimate and confidence interval describe magnitude and precision on a specified scale. Readers should consider the sponsor's reported test alongside the recalculated effect-scale summary and the underlying counts. Neither p-value provides a probability that the treatment strategies are equivalent or that a difference is clinically important.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists five outcome measures and five analyses, and names death, reinfarction, and stroke as secondary outcomes. It does not report a multiplicity procedure, a testing hierarchy, or a statement that secondary outcomes were intended as confirmatory. When several outcomes are tested, interpreting each without adjustment can make chance findings more likely across the set. In general, multiplicity procedures can address this issue, but no such procedure should be assumed when it is not described.

The record also does not report interim analyses, stopping rules, or whether any adjustments to the analysis plan occurred. These details matter because repeated examination of accumulating data or changes in outcome selection can affect interpretation. Their absence from the registry record does not show that such procedures did or did not occur; it means the record does not document them.

For the primary endpoint, the registry describes an intention-to-treat analysis and specifies inclusion of patients with electrocardiograms suitable for analysis at both inclusion and 120 minutes afterward. It does not report the number of participants lacking suitable recordings, the reasons recordings were unavailable, or a method for handling missing measurements. Nor does it explain how the stated intention-to-treat basis relates to restricting the endpoint analysis to participants with both recordings available.

For the secondary outcomes, denominators are reported for the two arms, but the record does not explain missing-data handling or whether all enrolled participants were followed for every outcome. The registry does not report a full statistical analysis plan, including covariate adjustment or sensitivity analyses. Without those details, it is not possible to assess how robust the results are to alternative missing-data assumptions or analysis choices.

These reporting gaps affect confidence in the completeness and confirmatory status of the analyses. They do not change the observed counts, but they limit what can be concluded about the analysis process and the extent to which the reported findings were prespecified.

16. What the Result Does, and Does Not, Mean

The primary result describes the proportion of analyzed participants who reached a defined electrocardiographic response threshold at 120 minutes after inclusion. In these data, the observed proportion is higher in the invasive group than in the thrombolysis group. The estimated risk difference is 0.062, but its 95% confidence interval, from -0.089 to 0.214, includes no difference and values in either direction. This is evidence of uncertainty, not a precise estimate of a stable treatment effect.

The result does not establish that the strategies are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether differences are small enough to fall within that margin; neither is reported in the registry record. Likewise, the result does not establish superiority or prove that one strategy is clinically better. A p-value alone cannot answer those questions, and the clinical importance of a risk difference cannot be judged without a meaningful threshold and relevant clinical context.

The primary endpoint is an early marker, not one of the listed 30-day clinical events. The registry also reports death, reinfarction, and stroke, but the event counts are sparse and the secondary comparisons are subject to uncertainty and unreported multiplicity procedures. The findings should not be combined into a claim that a change in the electrocardiographic endpoint necessarily leads to a change in later clinical outcomes.

The trial record gives useful information about the randomized comparison, endpoint definition, counts, and reported analysis. It gives less information about the original sample-size rationale, missing measurements, and complete analysis plan. These limitations make cautious interpretation appropriate. The statistics describe the posted results and their precision; they do not provide medical advice or a recommendation for individual care.

17. Why This Trial Matters Statistically

This trial is statistically informative because its primary result illustrates the distinction between an observed difference and a precise estimate of that difference. The invasive group had a numerically higher proportion meeting the ST-segment resolution threshold, but the confidence interval includes zero and allows differences in either direction. Reading only the point estimate would obscure that uncertainty; reading only a p-value would obscure the size and scale of the effect.

The endpoint also highlights the role of analysis populations. The registry calls the analysis intention to treat, while specifying that participants needed suitable electrocardiograms at inclusion and 120 minutes afterward. That combination raises a practical question about missing endpoint data and which participants contribute to the result. The record does not resolve it, demonstrating why transparent accounting of analyzed populations is important for interpreting randomized trials.

The secondary outcomes add another statistical lesson. Their event counts are sparse, and multiple outcomes are listed without a reported multiplicity approach. A consistent numerical direction across secondary counts may be noteworthy descriptively, but it does not remove the effects of imprecision or multiple testing. Statistical interpretation must distinguish a pattern that merits attention from confirmatory evidence.

Finally, the planning illustrations show how sample-size requirements depend on the effect chosen for detection and the desired power. Their figures are hypothetical and do not establish the trial's original assumptions. Together, these features make the record a useful example of evaluating effect size, uncertainty, endpoint availability, and the status of secondary analyses rather than relying on a single test result.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves important details of the trial's conduct and analysis unreported. Although it identifies randomized allocation and no masking, details about sequence generation, allocation concealment, adherence, and crossover are not reported in the registry record. Without those details, the risk of bias associated with implementation of the randomization and treatment pathways cannot be fully assessed from this record.

The primary outcome depends on electrocardiograms suitable for analysis at both inclusion and 120 minutes afterward. The registry does not report how many participants lacked suitable recordings or why they were unavailable. It also does not explain how this restriction was reconciled with the stated intention-to-treat basis. This leaves uncertainty about the extent and possible consequences of missing primary outcome data.

There is a difference between the overall enrollment of 205 and the arm-specific primary analysis denominators of 75 and 74. The endpoint eligibility description offers a possible reason for a more restricted analysis set, but the record does not provide a participant flow account or explain the denominator difference. Secondary outcome denominators are different, and the record does not explain the outcome-specific follow-up or missingness in further detail.

Other limitations include sparse secondary events, no reported multiplicity plan, and no reported original sample-size justification. The primary comparison has a wide confidence interval that includes zero, and the registry does not identify a threshold for clinical importance. Although the study objective mentions TIMI flow grade at mandated angiography 5 to 7 days after inclusion, the named primary result analyzed is ST-segment resolution; the record's full results for other outcome measures are not included in the registry record for this analysis.

The no-masking design is stated, but the registry record does not describe the procedures used to reduce bias in outcome assessment. These limitations constrain interpretation of the posted results and should not be mistaken for proof that any particular bias occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison Between Thrombolysis and Primary Percutaneous Coronary Intervention (PCI) to Treat ST-Segment Elevation Myocardial Infarction — NCT00806403.
• Registry record last updated 2008-12-10; status last verified 2008-11.
• Results first posted 2008-12-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed Phase 4 randomized, parallel-group trial with no masking and enrollment of 205 participants. It compares a thrombolysis strategy, listing reteplase 10+10 U, with an invasive strategy involving primary PCI. The stated objective concerns early treatment and ST-segment resolution at 120 minutes, as well as TIMI flow grade at coronary angiography 5 to 7 days after inclusion.

The posted primary result counts participants with at least 50% ST-segment elevation resolution. The invasive group has a numerically higher observed proportion, but the recalculated risk-difference interval includes zero and spans effects in either direction. The registry reports a Fisher Exact p-value of 0.56, while the unadjusted recalculation gives p = 0.421.

Death, reinfarction, and stroke are listed as secondary outcomes at 30 days. Their event counts are sparse, and the record does not report a multiplicity plan or detailed missing-data procedures. The primary endpoint analysis population is restricted to participants with suitable electrocardiograms at both measurement times; further explanation of the denominators is not reported in the registry record.